Trichomonas Vaginalis Recurrence Among HIV+ Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trichomonas Vaginalis Recurrence Among HIV+ Women (NCT01018095), a randomized phase 4 study. The primary outcome is TV Culture Positive Result.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel-group Phase IV trial sponsored by Tulane University Health Sciences Center. It lists enrollment as 270 and the status as completed. The recorded study start is 2005-05, and the primary completion date is 2009-07. The trial compared two metronidazole regimens among HIV-infected women with Trichomonas vaginalis infection: a single dose of 2 gm and a 500 mg dose x 7 days.

The primary outcome was a positive Trichomonas vaginalis culture at the test-of-cure visit, scheduled 6-12 days after treatment completion. The outcome population is described as participants who returned for that visit. The posted arm counts for this outcome are 130 for the seven-day group and 125 for the single-dose group. These are outcome-analysis counts, not a replacement for the registry’s overall enrollment figure. The record does not explain the difference between the enrollment figure and the endpoint counts, or report the reasons participants may not have contributed to the primary endpoint.

The registry lists two outcome measures and three analyses. It also lists a secondary culture-positive outcome at 3 months post-enrollment. Randomization and single masking are reported, but the method used to generate the allocation sequence, conceal allocation, or maintain masking is not reported in the registry record. Details of the trial’s original statistical plan, including its sample-size justification and any planned interim analyses, are not reported. The record’s analysis labels and reported results can be described, but the available information does not establish every element of the planned design or analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Participants who returned for their test of cure visit

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as TV Culture Positive Result, measured over test-of-cure visit at 6-12 days post-treatment completion.

The primary endpoint counts participants with a positive Trichomonas vaginalis culture at the test-of-cure visit. The registry says participants were screened using an InPouch culture and that the presence of the parasite yields a positive result. The visit was scheduled 6-12 days after treatment completion. This is a binary outcome: for this measure, each participant is classified as having a positive culture or not having a positive culture.

A culture-based endpoint provides a direct laboratory measure of whether the parasite was detected at the specified follow-up visit. It is distinct from a report of symptoms or a broader judgment about clinical status. A positive test at this time point does not, by itself, establish why the culture was positive. The registry record does not report whether a positive culture represents persistence, recurrence, or another explanation, so those possibilities should not be treated as interchangeable conclusions from this endpoint.

The endpoint is analyzed among participants who returned for the test-of-cure visit. That matters because the result describes the tested population, and not automatically every participant enrolled or randomized. The registry record does not report the outcomes of participants without a test-of-cure result or describe an imputation procedure for missing results. As a result, interpretation should keep the visit-specific measurement and the reported analysis population in view.

7. Results Posted in the Registry

• Single Dose: 16.8% (21/125) versus 8.5% (11/130) on control; risk difference 8.3 percentage points (95% CI 0.2 to 16.5), risk ratio 1.99 (1.00–3.95); unadjusted two-proportion z-test p = 0.045.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

TV Culture Positive Result

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Single Dose: 24.1% (19/79) versus 11.0% (8/73) on control; risk difference 13.1 percentage points (95% CI 1.3 to 24.9), risk ratio 2.19 (1.02–4.70); unadjusted two-proportion z-test p = 0.035.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Single Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts a secondary culture-positive outcome at 3 months post-enrollment. Its comparison has the same broad direction as the primary endpoint: the single-dose group has a higher culture-positive result than the seven-day group in the posted counts. This directional consistency is relevant, but the secondary endpoint is measured at a different time point and has its own set of participants with outcome data. It should not be treated as a duplicate measurement of the primary test-of-cure endpoint.

The secondary result provides a later follow-up perspective, while the primary endpoint concerns culture status at the test-of-cure visit 6-12 days after treatment completion. The secondary analysis therefore addresses a distinct time-specific observation. The registry does not report enough information to determine why participants do not appear in the secondary analysis counts or how missing follow-up outcomes were handled. Differences in analysis populations and follow-up timing limit direct comparison between the endpoint estimates.

The secondary analysis is reported as an unadjusted result, and no multiplicity adjustment is reported in the registry record. In general, when several outcomes or analyses are examined, the chance of at least one apparently notable result can increase unless the analysis plan accounts for that multiplicity. A secondary finding is consequently more appropriately treated as supportive or exploratory than as an independent confirmation of the primary result, especially when its analysis plan and role in the testing hierarchy are not reported.

The secondary result’s direction can be considered alongside the primary pattern, but it does not resolve the discrepancy between the primary re-calculation and sponsor-reported analyses. Nor does it establish a mechanism for positive cultures or justify extending the finding beyond the measured visits and population. The registry record lists one posted secondary outcome; it does not provide a complete account of all outcomes that may have been assessed during the trial.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• TV Culture Positive Result

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a binary outcome: a participant either had a positive culture at the test-of-cure visit or did not. The reported arm counts and the re-calculated comparison therefore concern proportions of participants, rather than a continuous measurement such as a laboratory concentration. The registry reports a risk-difference re-calculation comparing single dose with seven-day treatment, as well as risk-ratio analyses in the sponsor-reported results.

What does a risk difference describe?

In general, a risk difference subtracts the event proportion in one group from the event proportion in the comparison group. Its sign depends on which group is subtracted from which, so the stated comparison direction is essential. A positive risk difference for single dose relative to seven-day treatment means that the observed event proportion is higher in the single-dose group. The re-calculated risk difference is an unadjusted comparison from the posted summary counts, not an adjusted estimate accounting for other characteristics.

What does a risk ratio describe?

In general, a risk ratio divides one group’s event proportion by the other group’s event proportion. A ratio below one means the numerator group’s event proportion is lower than the denominator group’s, while a ratio above one means it is higher. That interpretation depends on the numerator and denominator ordering. The registry reports risk ratios but does not explain the group ordering in enough detail to make them directly interchangeable with the re-calculated risk difference’s stated direction. The differing numerical presentations should therefore remain attributed to their respective analyses.

How should confidence intervals and p-values be read?

In general, a confidence interval gives a range of values compatible with the data and the statistical method under its assumptions. It conveys uncertainty about an estimate; it is not a range containing a guaranteed proportion of future trial results, nor does it account for every source of uncertainty. For a risk difference, an interval that reaches zero is commonly understood as including no difference under the corresponding two-sided test. The re-calculated interval’s lower limit is just above zero, while the registry-reported intervals differ across the analyses. This is one reason the discrepancy should not be ignored.

In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. It does not measure the probability that the null hypothesis is true, the probability that a result is due to chance, or the size of a treatment effect. The registry reports p = .045 for one analysis and p <0.05 for another; the unadjusted re-calculation also gives p = 0.045. The numerical proximity of these values does not make the estimates or methods identical.

What is the role of the chi-squared analysis?

In general, a chi-squared test evaluates whether categorical outcome frequencies differ across groups under its assumptions. The registry labels one reported analysis “Chi-squared” and gives a risk ratio as its parameter. The record does not describe the exact test implementation or any adjustments. It is therefore appropriate to identify the method as the registry does, without assuming unreported details about corrections, covariate adjustment, or analysis populations.

What do non-inferiority and equivalence labels require?

In general, a non-inferiority analysis asks whether an intervention is not worse than a comparator by more than a prespecified margin. An equivalence analysis asks whether the difference is contained within prespecified bounds. Those are not established simply by a nonsignificant difference or by an interval that happens to include a particular value. The margin, hypothesis formulation, confidence-interval rule, and analysis population are essential to interpretation. Although the registry labels its reported analyses as non-inferiority or equivalence analyses, those details are not reported in the registry record. The label alone is not enough to verify that the intended criterion was met.

The disagreement between the simple unadjusted re-calculation and the registry’s reported analyses also matters methodologically. The re-calculation is derived from posted summary statistics, whereas the reported analyses are the sponsor’s own analyses. The registry record marks a discrepancy; under that circumstance, the sponsor’s own analysis takes precedence. The re-calculation remains useful as a transparent check on how the posted counts compare, but it should not be presented as the definitive trial analysis or used to replace the sponsor’s result.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the data and the chosen statistical method. A confidence interval conveys this uncertainty by giving a range of estimates compatible with the observed information and assumptions. Wider intervals indicate less precision than narrower intervals, all else being equal. Precision is not the same as clinical importance, and a narrow interval cannot remedy a mismatch between the analysis and the question of interest.

For the primary endpoint, the simple unadjusted re-calculation gives a risk-difference interval whose lower limit is just above zero. This indicates that the re-calculated interval lies on the positive side for single dose relative to seven-day treatment, but the interval’s upper limit is appreciably farther from zero than its lower limit. The estimate should therefore be read together with the interval, rather than as a certain or exact treatment contrast. The re-calculation is based on posted summary counts and is not the sponsor’s own analysis.

The registry reports a risk ratio of 0.5 with a 95% confidence interval from 0.25 to 1.00, and a separate risk ratio of 0.46 with a 95% confidence interval from 0.21 to 0.98. These are not the same estimate or interval, and their relationship to the re-calculated direction depends on the group ordering and analysis method. The registry record flags a discrepancy, so the sponsor’s reported analysis takes precedence over the re-calculation. The different reported intervals also mean that the choice of analysis affects the apparent precision and whether an interval reaches its null value.

Confidence intervals do not incorporate every limitation. In particular, they do not resolve uncertainty about missing test-of-cure results, unreported analysis choices, the non-inferiority or equivalence margin, or whether the reported analysis population matches the intended estimand. The registry record does not report those details. The intervals should thus be understood as method-specific statistical summaries, not as a complete measure of all uncertainty surrounding the trial’s interpretation.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For this binary outcome, the figures are participants per arm, not total events. They should not be read as the number enrolled in the completed trial or as a reconstruction of its actual planning assumptions.

The 80% power column gives the illustrative participants per arm for a design with an 80% chance of detecting the chosen effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding illustration for a 90% chance. These are design calculations, not guarantees about a future study. The row for 100% of the observed effect uses the full observed effect as the target; the rows for 75% and 50% use smaller fractions of it. Smaller effects need more participants to detect under otherwise unchanged assumptions, which is why the illustrations increase as the target effect becomes smaller.

The figures are not observed power. They do not tell how much power the completed trial had after seeing its results, and they do not validate the estimated effect used in the illustration. Because the observed effect can be unstable, particularly when derived from one trial, these calculations are best treated as conditional planning scenarios. The registry record does not report the trial’s own original sample-size assumptions or justification.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.085; treatment proportion p₁ = 0.168; average p̄ = 0.126.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4698 = 0.9208.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4661 = 0.3923.
4. n = (0.9208 + 0.3923)² / (0.0834)² = 248.0, rounded up to 248 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0846153846153846                          # control proportion
p1 <- 0.168                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1018095)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 248 (80% power), 332 (90% power)
 75% of observed effect: n per arm = 411 (80% power), 549 (90% power)
 50% of observed effect: n per arm = 851 (80% power), 1,139 (90% power)
power.prop.test: 248 
Simulated power at n = 248 per arm: 0.804 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry contains sponsor-reported analyses and a simple unadjusted re-calculation from the posted primary summary counts. The re-calculation describes the single-dose versus seven-day contrast as a positive risk difference, with an unadjusted p-value of 0.045. The sponsor-reported results instead present risk ratios, including one from a relative-risk method and one associated with a chi-squared method. The estimates and intervals are not identical to the re-calculated comparison.

The record explicitly flags a discrepancy. Accordingly, the sponsor’s own analysis takes precedence over the re-calculation when describing the trial’s reported statistical result. This does not mean the discrepancy disappears or that the re-calculation is irrelevant: it shows that the posted counts and analysis summaries do not yield a single uniform statistical account. The registry record does not provide enough detail to reconcile the differences, including all analysis specifications and group ordering.

The sponsor’s analyses are labeled non-inferiority or equivalence, but the registry record does not report the margin or full decision rule. It is therefore possible to report the sponsor’s estimates and their stated labels, but not to verify the non-inferiority or equivalence claim from the available record alone. The sponsor analysis should be distinguished from the arithmetic re-calculation, and neither should be expanded into a claim beyond its reported result.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, groups, or statistical analyses are considered. In general, examining more than one statistical question can increase the chance that at least one result appears noteworthy even when there is no corresponding underlying difference. Prespecifying a primary outcome and a testing hierarchy, or using an appropriate adjustment, can help control that issue. The registry lists a primary outcome, a secondary outcome, and multiple analyses, but a full multiplicity strategy is not reported in the registry record.

The record does not report whether the secondary outcome was part of a confirmatory testing sequence, whether any adjustment was planned, or whether all outcomes and analyses are posted. The secondary p-value is described as unadjusted in the posted comparison. It should therefore not be interpreted as though it had been protected against multiple testing. This limitation is separate from the discrepancy in the primary analyses: multiplicity adjustment would not, by itself, explain or reconcile different methods and estimates for the same endpoint.

Missing data and analysis populations also affect interpretation. The primary endpoint population is described as participants who returned for the test-of-cure visit. The registry reports arm-level outcome counts, but it does not report the outcome status of those without a test-of-cure result, reasons for non-return, or a method for handling missing outcomes. It also does not report whether the primary analysis followed an intention-to-treat, per-protocol, or other specified population definition. Those details are especially relevant when interpreting analyses labeled non-inferiority or equivalence, because the choice of analysis population can affect such conclusions.

The secondary endpoint has a different follow-up time and different posted arm counts. The registry record does not describe the handling of missing secondary follow-up, or whether participants with an outcome at one time point were required to contribute at another. It is not appropriate to assume that missing outcomes were absent, negative, or otherwise resolved in a particular way. The available information supports describing the recorded outcomes and analysis labels, while leaving these missing-data and multiplicity questions open.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

The registry’s serious-adverse-event summary reports zero serious adverse events in the seven-day group and zero in the single-dose group, with 135 participants at risk listed for each group. The “other adverse events” counts are also recorded as zero in both groups, with 135 at risk in each. These figures describe what the registry reports for the stated at-risk groups; they do not establish that no adverse events of any kind occurred outside the categories or reporting scope represented by these fields.

Deaths are listed as null rather than as a numerical count. The registry record does not report a death count in these fields, so null should not be interpreted as a confirmed count of zero. No serious-adverse-event terms are listed. The record does not provide additional event descriptions, definitions, collection procedures, or a narrative explaining the safety findings. The figures should be read as registry reporting, not as a comprehensive characterization of the regimens’ safety.

These safety entries are separate from the primary culture-positive endpoint. The at-risk counts in the adverse-event summary should not be substituted for the primary test-of-cure population counts. As with any safety summary, absence of reported events in a registry field is not proof that a treatment has no risks.

17. What the Result Does, and Does Not, Mean

The results describe a randomized comparison of two metronidazole regimens and a laboratory endpoint measured at a defined test-of-cure visit. The posted primary counts show more positive cultures in the single-dose arm than in the seven-day arm among participants with reported endpoint results. A simple unadjusted re-calculation gives a positive risk difference in that comparison, while the registry’s sponsor-reported analyses present risk ratios and are labeled as non-inferiority or equivalence analyses.

The record also flags a discrepancy between the posted counts and reported analyses. The sponsor’s own analysis takes precedence over the re-calculation, but the discrepancy remains important to readers. The registry does not report the details needed to reconcile the estimates or fully evaluate the non-inferiority/equivalence framework, including the margin and complete decision rule. The results therefore should not be compressed into a simple claim that the regimens are equivalent or that one is definitively better based only on the available registry information.

The endpoint captures culture positivity at a particular follow-up visit among participants who returned. It does not establish longer-term status for every enrolled participant, and the registry record does not specify whether a positive culture should be understood as persistence, recurrence, or another explanation. The secondary result concerns a later time point, but its different follow-up population and unadjusted analysis mean it cannot resolve those limits or serve as a direct substitute for the primary endpoint.

Statistical significance, confidence intervals, and observed event counts each convey different information. A p-value does not measure the size or importance of an effect, and a confidence interval reflects uncertainty under a particular method rather than every source of uncertainty. The registry’s reported safety fields record no serious or other adverse events in the stated groups, but deaths are not reported numerically and the fields are not a complete safety narrative.

Accordingly, the registry supports a careful description of the recorded culture results, sponsor analyses, and their limitations. It does not by itself settle the intended non-inferiority or equivalence question, establish outcomes beyond the measured visits, or provide medical advice.

18. Why This Trial Matters Statistically

This trial illustrates why a statistical result should be read together with its endpoint, analysis population, and reporting context. The primary outcome is a culture result at a specified visit, not a general measure of health or a long-term outcome. The analysis population is restricted to participants who returned for test of cure, which makes clear that the posted endpoint result is tied to observed follow-up.

It also demonstrates the importance of distinguishing a re-calculation from the trial’s own analysis. The posted counts can be used to describe an unadjusted risk-difference comparison, while the registry’s sponsor-reported results use risk ratios and carry non-inferiority/equivalence labels. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence. Yet the absence of the full analysis details and the non-inferiority/equivalence margin prevents a complete assessment of the stated inferential objective. A result’s label cannot replace the information needed to interpret its decision rule.

The record also provides an example of why uncertainty is not captured by a p-value alone. Confidence intervals differ across the reported analyses, and the interval’s relationship to a null value depends on the method and comparison direction. The secondary endpoint adds information at a later time point, but it is unadjusted and does not automatically offer independent confirmation. Finally, planning illustrations based on an observed effect are not the same as the trial’s original design assumptions or an estimate of observed power.

These distinctions are useful in clinical research because apparently straightforward comparisons can depend on outcome timing, analysis population, direction of contrast, and prespecified decision criteria. Careful reporting makes those dependencies visible and helps prevent a statistical summary from being interpreted more broadly than its data support.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific reporting gaps constrain interpretation. The registry describes randomization and single masking, but does not report the allocation-generation or concealment procedures, masking details, or adherence by treatment arm. The record also does not give the original sample-size justification, the planned statistical analysis in full, or whether interim analyses were conducted. These omissions prevent a complete comparison of the reported analyses with the intended protocol.

The primary outcome population consists of participants who returned for test of cure. The registry does not explain why endpoint counts differ from overall enrollment, report the reasons for missing test-of-cure data, or describe missing-data handling. It does not identify whether the analysis population was intention-to-treat, per-protocol, or another prespecified group. These gaps matter particularly for the registry’s non-inferiority/equivalence labels.

The record marks a discrepancy between the posted summary counts and sponsor-reported analyses. It does not supply enough methodological detail to reconcile that discrepancy, including the complete group ordering and analysis specifications. The non-inferiority/equivalence margin and decision rule are also not reported, so the labels cannot be fully evaluated from the registry record alone.

The secondary culture outcome is measured at a different time point and has a distinct analysis population. Missing follow-up handling and multiplicity procedures are not reported. The safety summary contains zero counts for serious and other adverse events in the listed at-risk groups, but deaths are null and there is no detailed safety narrative. These limits make the registry useful for describing its posted results, but insufficient for resolving every methodological or clinical interpretation question.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trichomonas Vaginalis Recurrence Among HIV+ Women — NCT01018095.
• Registry record last updated 2016-12-20; status last verified 2016-12.
• Results first posted 2013-07-15.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed randomized, single-masked, parallel-group Phase IV trial of metronidazole single dose versus a seven-day dose among HIV-infected women with Trichomonas vaginalis infection. The primary outcome was a positive culture at the test-of-cure visit 6-12 days after treatment completion, among participants who returned for that visit.

The posted primary counts show more culture-positive results in the single-dose group. A simple unadjusted re-calculation differs in presentation from the sponsor-reported risk-ratio analyses, and the registry flags a discrepancy. The sponsor’s own analysis takes precedence, but the record does not report the margin and full decision rule needed to assess the non-inferiority/equivalence labels. A secondary culture outcome is listed at 3 months post-enrollment. Missing-data, multiplicity, and several analysis-plan details are not reported in the registry record.